Today Gregor Mendel is a towering hero of biology, and yet during his own lifetime his ideas about heredity were greeted with deafening silence. In hindsight, it’s easy to blame his obscurity on his peers, and to say that they were simply unable to grasp his discoveries. But that’s not entirely true. Mendel got his ideas about heredity by experimenting on pea plants. If he crossed a plant with wrinkled peas with one with smooth peas, for example, the next generation produced only smooth peas. But when Mendel bred the hybrids, some of the following generation produced wrinkled peas again. Mendel argued that each parent must pass down factors to its offspring which didn’t merge with the factors from the other parent. For some reason, a plant only produced wrinkled peas if it inherited two wrinkle-factors.

Hoping to draw some attention to his research, Mendel wrote to Karl von Nageli, a prominent German botanist. Von Nageli was slow to respond, and when he did, he suggested that Mendel try to get the same results from hawkweed (Hieracium), the plant that von Nageli had studied for decades. Mendel tried and failed. It’s impossible to say whether von Nageli would have helped spread the word about Mendel’s work if the hawkweed experiments had worked out, but their failure couldn’t have helped.

After Mendel’s death, a new generation of biologists discovered his work and, with the insights they had gathered from their own work, they realized he had actually been onto something. Pea plants really do pass on factors–genes–to their offspring, and sometimes the genes affect the appearance of the plants and sometimes they don’t. Mendelian heredity, as it came to be known, was instrumental in the rise of the new science of genetics, and today practically every high school biology class features charts showing how dominant and recessive alleles are passed down from one generation to the next. Mendelian heredity also helped explain how new mutations could spread through a population–the first step in evolutionary change.

But what about that hawkweed? It turns out that usually Hieracium reproduces very differently than peas. A mature Hieracium does not need to mate with another plant. It does not even need to fertilize itself. Instead, it simply produces clones of itself. If Nageli had happened to have studied a plant that reproduced like peas, Mendel would have had more luck.

Hawkweed raises an important question–one that is particularly important this morning. Does it tells us that Mendel was wrong? Should teachers throw their Mendelian charts into the fire? No. Mendel found a pattern that is widespread in nature, but not a universal law. Most animals are pretty obedient to Mendel’s rule, as are many plants. Many algae and other protozoans also have Mendelian heredity, although many don’t. Many clone themselves. And among bacteria and archaea, which make up most of the diversity of life, Mendelian heredity is missing altogether. Bacteria and archaea often clone themselves, trade genes, and in some cases the microbes even merge together into a giant mass of DNA that then gives rise to spores.

Today in Nature, scientists found another exception to Mendelian heredity. They studied a plant called Arabidopsis (also known as cress) much as Mendel did, tracing genes from one generation to the next. They crossed two lines of cress, and then allowed the hybrids to self-fertilize for two more generations. Some of the versions of the genes disappeared over the generations from the genomes of the plants, as you’d expect. But then something weird happened: in a new generation of plants, some of the vanished genes reappeared. The authors think that the vanished genes must have been hiding somewhere–perhaps encoded as RNA–and were then tranformed back into DNA.

Is cress the tip of a genetic iceberg (to mix my metaphors hideously)? Only more experiments will tell. If it is more than just a fluke, it may turn out to play an important part in evolution, joining some other weird mechanisms, such as "adaptive mutation," in which bacteria crank up their mutation rate when they undergo stress. But hold onto those Mendelian charts. These cress plants are wonderfully weird–but no more wonderfully weird than hawkweed.

Don’t believe the hype. The authors of the Nature paper never considered and dismissed the possibility that selection was the cause of their high number of revertants. They found these refertants when the double mutants served as the pollen donor. If the HTH gene is important for success in pollen competition, then the high frequency of revertants can be explained by selection.

I haven’t read the paper, but the Nature news story says “And when the team studied numerous other genes, it found that the plants had often edited those back to their ancestral form too.” That argues against gamete evolution, which would require a rather high mutation rate in any event.

Why is RNA the suggested storehouse for the hypothesized information? Is it because DNA has been extensively searched for and not found?

PacRim, if I remember correctly, clonal species (at least in animals) tend to fare poorly for just that reason (though with parasites as the prime culprit).

For instance, clonal reproduction has popped up many times in Whiptail lizard (Cnemidophorus), but all clonal species are fairly recent, especially compared to the non-clonal species. The differences in how old the sexual vs asexual species are, to me, strongly indicates that asexual species are more likely to die out. (Of course, there may be other possible reasons I don’t know of.)

I was exceedingly skeptical of this report. This will certainly set off a frantic search for a mechanism, and in fact I’m shocked that the paper appeared in Nature without one. Many similarly-exciting works are rejected for just that reason, to such a high degree that folks doing work that they expect to submit to Nature will often work frantically on the mechanism angle before they even bother submitting.

When a mechanism does turn up I will present it at my next departmental journal club. Until then I’m simply too skeptical that something more parsimonious, errant pollen, for example, didn’t cause this.

If even sexual reproduction is mainly geared towards fidelity of reproduction, using the other sex more as a source of clean copies than the chance of generating something particularly new, it makes sense that they will keep finding mutation reversing mechanisms. Randomizing genetic material can’t really be good, so there might be assumed to be more mechanisms undiscovered, by which such randomizations are corrected to their original configuration. Sex itself, could one day be determined to be one of these, in its overall aspect.

Wow… highly unorthodox and controvertial! If proven right, this could shift paradigm.

I agree with Tim to a certain extent that the authors extensively elminiated many possibilities, but couldn’t come up with one mechanism to explain the observation. Nature, along with other high profile journals, tends to publish hot, sexy papers. This could be the big thing, or one hit wonder.

Let’s give the authors some credits, however. They could have dismissed their observations, because they couldn’t be explained neatly. They must have endured a lot of adversities to reach this point. They actually did a lot of experiments, even though it may not be apparent in the published paper, as is typical with many genetics paper.

If true, this is really something.

Desirable future researches:

1. Genetic screen to identify suppressors of hth. Can you think of any biology involving just one gene? Most, if not all, of biological phenomena happen in the context of network or pathways. Especially, when the HOTHEAD doesn’t seem to mediate reversions directly.

2. Seek for the similar phenomena in other organisms. If not conserved through the evolution, what’s the implication or significance?

3. If RNAs are used as templates, then there must be an RNA-dependent DNA polymerase doing this job. Does a highly advanced organism like cress could have such an enzyme?

The authors specifically ruled out selection for traditional revertants as the rate of silent mutations was not increased, additionally they identified high level of reversion for sequences unrelated to the hth allele but the reversion rates were dependent on the hth backgroud. Doesn’t this rule out selection?

-n, in response to your last point: it seems vanishingly unlikely that this phenomenon would turn up in Drosophila or yeast. I will ask better geneticists than myself about this the next time I have an opportunity, but on first principles I’d say that enough work has been done in those two model systems that this ‘un-mutation’ event would have been seen already.

I’d focus on what distinguishes plant systems from the other major model systems. One is that in most everything else reproduction requires organism-to-to-organism contact and is easily excluded when you don’t want it. Pollen strikes me as a lot harder to control than loose flies. The second is the issue of ploidy. Plants are known to spontaneously increase or decrease their genome copy number and some, corn for example, have ploidy numbers that are absolutely ridiculous. I wonder whether this result might come from some aspect of genome duplication – a mosaic plant, for example, in which the portion tested did not have the WT gene but some other part kept a copy.

Tim, the ploidy issue was the first thing that came to my mind… before reading the paper. As you mentioned, plants are notorious for this. However, the authors addressed this with Southern blot to show there is only one gene for HTH. If there is a pseudogene, it is most likely to show distinct restriction patterns from those of the HTH. So it was out of question in my mind. I don’t know what you think about this.

I would agree that this phenomenon might not be observed in flies, which reproduce exclusively by sex. I wouldn’t bet on yeast, though. Saccharomyces has no problem reproducing asexually. HTH thing could be restricted to organisms with asexual reproduction…

Whether or not the scientific result is right, the sociological aspects point up an important moral for creationists: you’re a lot more likely to overturn a scientific law by doing actual science than by lobbying the local school boards.

As an author, you may find it interesting to read the real story of Mendel in the book, Einstein’s Luck. These are not Mendel’s rules we are discussing here. But back to the arabidopsis paper.

As a cancer geneticist who spends a lot of time trying to expunge mutation artifacts from our genetic studies, I?m appalled at the sloppy presentation of the arabidopsis reversions in Nature. No supplemental data, a methods
section shorter than the Abstract, near-absence of methodologic details in the text, etc.

In the first paragraph of the second page, did they really use allele-specific PCR to ?clearly? show a conclusion? In other words, they purchased the chosen sequence by mail, then found the same sequence when the mail-order oligos were used in an artifact-prone method? All without showing any controls for the specificity of the allele-specific method or for how the results might be potentially affected by small sample size (which by reducing the number of DNA templates, increases the influence of PCR-introduced errors).

In figure 1a, what was the restriction site used? Did it occur naturally in the sequence (I don?t see it in the figure showing the sequences), or was it artifactually introduced during PCR? Why does the top allele in Figure 1A appear so much brighter than the restriction-cut allele just below it – are the alleles not in molar equivalence? If this is a two-allele system, molar
equivalence would seem to be required.

In the Southern blot, what was the probe?

What were the primer sequences used for the assays ?

If the altered sequences were found by one method, could they be confirmed by finding them with use of another method having non-overlapping artifactual tendencies? I note that they didn?t use phage lifts or allele-specific ligation to quantitate the allelic ratio of the revertant alleles, as had been done 15 years earlier to provide the necessary controls for the study that showed infrequent mutant genes in stool samples of colorectal cancer patients.

Why no negative controls – such as non-embryoid parts of the hth/hth and HTH/HTH plants whose DNA had been isolated in minute amounts similar to the technique used for the seeds (would exclude both small-sample amplification artifacts and chimerism)?

Why no primary data from gene sequencing in any of the figures? Did Nature refuse to publish the primary data even in supplemental form?

Do we really think that 38% of samples had gene reversion (table 2)? That would be a higher rate of gene conversion in trans than any other recombination system, including yeast.

Why no coded samples? When the infrequent gene mutations in pancreatic ductal lesions and in stool samples of pancreatic cancer patients were found 10 years ago, the samples were tested blindly. Wouldn?t everyone would do this or some similar form of investigator blinding? And why not do the studies in a lab that had never previously seen studies of the HTH gene? This has been done when other authors wanted to quantitate gene mutation prevalence rates in cancer patients.

I suppose Nature will once again call in the Amazing Randi to investigate the authors, just like they did with their water memory paper in 1988.

I don?t claim to know whether the data in this paper are valid, but certainly the methods are not presented in adequate detail nor in adequate confirmatory depth to judge. Until then, discussing this paper is a waste of time.

i don’t see how it can be selection or an increased mutation rate if its genomewide reversion observed in the F2 generation to polymorphisms only present in one or other F0 grandparents.

However selection after the action of any non-mendelian restorative mechanism may explain the high percentage of revertants (as high as 38% criticised by Scott Kern, whose general point of lack of transparency i agree is a general problem with Nature and co). Revertant gametes may be healthier with one correct copy of Hothead rather than the mechanism itself being quite so ‘hot’ at its job. This is supported by the much lower reversion rate (2%) observed for other markers in the absence of hothead (table 3) which probably don’t give a any selctive advantage to gametes. Also the double revertants at I can expand on this if it isn’t clear…

More generally as far as criticising the paper… well they have really stuck out there necks if they haven’t thought of all the right internal checks and controls. And its 7 years since there initial observation so they haven’t rushed it out. I am sure they are well aware that they are staking there reputations.

With all due respect, it seems to me that many of Prof. Kern’s criticisms are a bit over the top. For example, the intensity difference between the cleaved and uncleaved PCR products he complains about in Fig 1 is the same for the revertants and for the HTH/hth control.

From looking at the Genetics paper, I suspect that the restriction site is a CAPS polymorphism that is tightly linked to hth/HTH, and the hth mutation doesn’t destroy the site. Seeing this come back is part of the reason why one would suspect conversion instead of mutation.

The high “frequency” in Table 2 is clearly not a rigorously measured frequency. It should be remembered that there are many rounds of cell division from seed to pollen, and there could be jackpots and selection effects as suggested by others.

But for me, Table 3 is the key – the unselected polymorphisms are coverting in both directions. Even though these are not as high as 38%, they are still very high frequencies. But comparing rates to recombinational gene conversions from other systems isn’t really fair – 1) the authors are claiming that conversion from DNA is NOT the mechanism, 2) the events are undetectable in the HTH+ background, 3) there are examples of very high frequencies of conversions when there are directed ds breaks, as in mating type switching, and 4) plants are just different.

Prof Kern asks for other methods to examine the alleles. The DNA methods are the other method – the primary method is genetics – following the segregation of the HTH and hth phenotypes.

While it might be preferable in principle for all studies to be designed with blind testing of coded samples, it seems like overkill to demand that here. The hth plants are presumably readily obtained by anyone who wants to reproduce the results, which I am guessing is not the case with the patient samples Dr. Kern refers to.

I agree that the description of methods is weak, but I don’t really see a need for supplemental data here. It also seems to be well within the norm for Nature papers…sadly this seems to be the new norm for many journals. Still, my bottom line is that this is an very interesting result that is probably real…it also doesn’t upset the Mendelian paradigm any more than retroviruses or transposons do.